Sediment characteristics regulate anaerobic oxidation of methane coupled with nitrate and nitrite in the hyporheic zone

Wang, Yujia; Bajic, Maja; Wunderlich, Anja; Geist, Juergen; Orsi, William; Einsiedl, Florian

doi:10.5194/egusphere-2026-2718

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https://doi.org/10.5194/egusphere-2026-2718

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27 May 2026

| 27 May 2026

Status: this preprint is open for discussion and under review for Biogeosciences (BG).

Sediment characteristics regulate anaerobic oxidation of methane coupled with nitrate and nitrite in the hyporheic zone

Yujia Wang, Maja Bajic, Anja Wunderlich, Juergen Geist, William Orsi, and Florian Einsiedl

Abstract. Methane (CH₄) emissions from river systems contribute to the global greenhouse gas budget, but their contribution remains poorly constrained. Although proxies such as temperature, electron acceptor (EA) availability, and microbial communities are controlling factors, the role of the sediment characteristics (sediment permeability and organic carbon (OC) content) on anaerobic oxidation of methane (AOM) coupled with nitrate (NO₃^-)/nitrite (NO₂^-) is not well unterstood. Here, we investigated gravel-dominated, high-permeability sediments, where efficient advective transport promotes the deep penetration of terminal EAs such as oxygen (O₂), NO₃^- and sulfate (SO₄^2-) and inhibits microbial methane production. Conversely, hyporheic zone (HZ) sediment with fine-grained sediment was characterized by lower permeability, which restricts solute transport and facilitates diffusion-dominated processes and the development of anaerobic zones. Under these conditions, the presence of microbial available OC may support biological methane formation. Analyses of microbial communities of two profiles further indicate that also the distribution of methanogenic and methane-oxidizing taxa is closely linked to sediment permeability-controlled geochemical zonation. The 1D reactive transport modeling suggests that AOM with NO₃^- and NO₂^- as dominant EAs is selected for as a microbial process in the lower permeable sediments. Sediment permeability, therefore, regulated EA availability and, together with OC availability, shapes geochemical zonation, microbial community structure and the mechanism of AOM in the HZ. Therefore, sediment characteristics are shown here to strongly influence transport-reaction coupling, thereby regulating AOM and ultimately methane emissions from the HZ.

Received: 12 May 2026 – Discussion started: 27 May 2026

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Yujia Wang, Maja Bajic, Anja Wunderlich, Juergen Geist, William Orsi, and Florian Einsiedl

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RC1:
'Comment on egusphere-2026-2718', Anonymous Referee #1, 03 Jul 2026 reply
The manuscript investigates how sediment grain size and permeability affect methane production and oxidation in the hyporheic zone (HZ) of a gravel stream, and whether anaerobic oxidation of methane (AOM) coupled to nitrate/nitrite competes with aerobic oxidation. The authors deployed peepers in situ for high-resolution porewater chemistry, 13C-CH4, sediment characterization, and molecular microbiology. Two complementary 1-D models (PROFILE and PHREEQC) were then applied to infer the activity and mechanisms of methane oxidation. This integrative design across a managed permeability gradient is genuinely attractive, and methane source–sink dynamics in rivers is an important topic. Inspecting the figures, the authors have collected an intriguing and valuable dataset. However, the manuscript needs substantial writing improvement before it can be considered further. In particular, the Results and Discussion section is wordy and sometimes repetitive, which makes it difficult to read, and the language often lacks necessary scientific rigor. The results are mixed with a considerable amount of speculation and overinterpretation of activities and mechanisms. Overall, the evidence presented does not sufficiently support all interpretations the authors suggested. My detailed comments are given below.
Major comments
On overall writing
The Moosach River and its connected branches, and even DAMO processes, have been studied previously, in part also by the authors' own group. The Introduction should therefore state precisely what is new in this study and properly summarize the relevant prior findings on the same field site. In addition, the motivation for investigating this topic, and the specific hypotheses being tested, should also be made explicit. Moreover, the scope of the study needs to be more clearly defined. Only two sites (B and C) are discussed in detail, some conclusions may be specific to this case study, and such limitations should be better acknowledged.

I recommend a clearer separation of the results from the discussion. Even if the authors choose to combine them, it would be much easier to read if the results were always presented first within each paragraph, followed by the discussion.

On hydrology and environment
The manuscript uses many hydrological and hydraulic terms, but none of the key parameters are actually properly described in the main text. Basic hydrological data (stream order, discharge, temperature, permeability, hydraulic conductivity, hydraulic gradient in the sediment, and related parameters) should be reported in numbers in the main text. Whether site C is diffusion-limited needs to be better defined.

Ebullition is also a primary methane transport pathway and introduced by the authors. It can export more methane to the atmosphere than diffusion, with much of the bubble-transported methane escaping microbial oxidation at the sediment surface. However, its role is not mentioned after the Introduction. Given that the authors report methane supersaturation and infer free-gas formation at site C, the potential contribution of ebullition should be discussed.

On microbiology
Function and activity (rates) should not be inferred from 16S relative abundance. The DAMO conclusion leans on the relative abundances of Methylomirabilis and Crenothrix, but amplicon abundance reflects presence more than activity. The authors already note this for aerobic methanotrophs, so the same caution applies also to NO₂-DAMO paragraphs, and the limitation should be discussed explicitly. To strengthen the functional interpretation, the authors could add absolute-abundance data from qPCR targeting functional genes (e.g. mcrA for methanogens, pmoA, or Methylomirabilis-specific 16S/pmoCABC or assays). Alternatively, a ¹³CH₄ tracer incubation with the same sediments would also be helpful for an activity story.

Dissimilatory nitrate reduction to ammonium (DNRA) is not considered at all. Organic matter mineralization is a plausible ammonium source, but in the nitrate-reducing interval DNRA is a competing sink that should be addressed. This matters because the balance between DNRA and denitrification changes the nitrogen fate and nitrogen budget.

There is an internal contradiction regarding aerobic methane oxidation at site C. The microbial composition is interpreted as favouring methanotrophs (eg, Line 569: "This spatial relationship provides compelling microbiological evidence for active MOx in the shallow sediment"), yet the PHREEQC model assigns MOx no contribution. This discrepancy needs to be explained.

The authors state that they "assume heterotrophic nitrate reduction… in which OC may serve as the electron donor." Porewater DOC was not measured, OC reactivity was not characterized, and no 15N data. Heterotrophic denitrification is therefore one possibility among several and should be presented as a hypothesis rather than asserted as established. Similarly, no sulfide was measured, there are no sulfur isotope data, and no rates are reported. A decrease in sulfate can also result from dilution or mixing (have you tried to calculate SO₄²⁻/Cl⁻ ratio?). In short, the nitrogen and sulfur mechanistic claims should either be much more softened or supported with more

On modelling
The rationale for using two models, and how their respective results enhance the study findings, needs to be further

I am not a modeler, but as I understand it, the PHREEQC model includes advection, whereas PROFILE considers only diffusion (with bioturbation and irrigation set to zero). At site B, however, advection matters, and PROFILE's neglect of it is the most likely origin of the alternating nitrate and sulfate "source" terms. This and whether it is legit to claim “two models ‘agree’ with each other” needs to be clarified.

Nitrite concentrations below the detection limit could suggest efficient and consistent complete denitrification (nitrite simply not accumulating) or with a detection limit that is too high. Interpreting below detection limit nitrite as evidence for rapid nitrite turnover, and then feeding this interpretation into a model whose result depends on rapid nitrite turnover, is like a circle. The concentration data do not independently support the model, and the text presents it as though they do.

The dominance of NO2-DAMO (>99% of methane oxidation) appears to be dependent on parameters the authors chose, rather than completely demanded by the data. NO2-DAMO was assigned a high methane affinity (Kₛ,CH₄ = 0.005 mmol kg⁻¹ w), a value transplanted from a wastewater study. It was supplied with nitrite through a allocation parameter (f_NO₂ = 0.50), but it was assigned the smallest biomass of any guild (Table S7). Such a parameter choice needs to be justified.

Other comments
Is plant material present in the streambed? Methanol derived from pectin in terrestrial plant material could be a key substrate supporting methane production, which may be relevant to the methanogenic pathway inferred here.

The use of methane carbon isotopes should be introduced in the Introduction.

The terminology for depth zones should be more consistent. Terms such as "shallow," "deep," and "reactive" should be defined and used consistently throughout. Please introduce clearly how many zones are defined, how the depth intervals are separated, and apply this scheme uniformly.

Methanoperedens / ANME-2d, the canonical NO₃-DAMO archaeon cited in the Introduction (eg, Line 44–46), is never reported in the Results. Was it absent from the sequencing data? This should be stated clearly.

Line 47: What kind of evidence is referred to here on Crenothrix , and in what type of river was the hyporheic zone studied?

Line 80: The authors should also justify why the hyporheic zone is defined as the top 40 cm.

Line 210: The version of the SILVA database used for taxonomic assignment must be specified.

Line 295: Does the absence of detectable methane necessarily indicate non-methanogenic conditions, or could it reflect the limited sampling depth? Please clarify.

Line 300-301: The claim that the OC is "aged" needs support. The statement that greater exchange coincides with less disturbance also appears contradictory and should be clarified.

Line 300: If permeability and OC content are used so extensively to interpret the results, their actual values should be reported in the main text rather than left in the Supplement.

Line 358: Please state clearly whether ¹³C-CH₄ becomes more depleted or more enriched with depth. It is a bit confusing here.

Figure 3: The sampling locations should be labelled directly on the panels for clarity.

Figure 3: Many Deltaproteobacteria are associated with sulfur cycling. Does the abundance of this group support the sulfate-reduction interpretation? Please comment.

Line 415: Interpreting oxygen utilization at the phylum level is an overinterpretation. Rather than relying on broad taxonomic groups, could the authors identify known functional groups for denitrification or sulfate reduction and check whether their abundances follow the described patterns?

Line 419: From the figure it is not possible to tell whether methanogenic taxa are present. Please make this clearer.

Line 531: The term "reaction intensity" should be defined.

The NMDS dispersion contrast is interpreted as niche diversity versus homogenization. This should be supported statistically (e.g. PERMANOVA together with a test of multivariate dispersion) rather than resting on the visual spread of the ordination.

Table S4: Each parameter should be defined explicitly for readers unfamiliar with these letters.

Reply
Citation: https://doi.org/10.5194/egusphere-2026-2718-RC1
RC2:
'Comment on egusphere-2026-2718', Anonymous Referee #2, 15 Jul 2026 reply
General comments
This study addresses an important and under-constrained question and brings together a valuable combination of porewater chemistry, stable isotopes, microbial analyses, and modeling. The field contrasts and depth-resolved measurements provide a useful descriptive picture of how sediment conditions are associated with redox zonation and methane accumulation. My main concern is that the manuscript often presents mechanistic and causal interpretations more strongly than the design, measurements, and modeling assumptions can support. The study would be substantially improved by aligning the conclusions more closely with the evidence, distinguishing direct observations from modeled interpretations, strengthening the statistical and uncertainty analysis, and revising the writing for greater clarity. I recommend major revisions, focused on recalibrating the conclusions to the evidence, moving the model's parameterization and sensitivity analysis into the main text, and strengthening the statistical and quantitative reporting.
Specific comments
PROFILE and PHREEQC are shown as jointly supporting the mechanistic conclusion, but the pathway-specific result comes only from PHREEQC. PROFILE identifies net electron-acceptor source–sink zones and cannot distinguish among heterotrophic denitrification, NO₃⁻-DAMO, NO₂⁻-DAMO, or overlapping processes. The models also do not appear to exchange parameters or constrain one another. They should therefore be described as parallel analyses rather than an integrated modeling framework, and the conclusion that AOM (particularly NO₂⁻-DAMO) dominates methane removal should be attributed explicitly to PHREEQC. This issue is present in multiple places in the paper. Example: "By integrating porewater chemistry, microbial community analysis, and inverse reactive transport modeling, this study further demonstrates that AOM represents the dominant methane sink..." attributes the dominance of AOM to the integration of porewater chemistry, microbial data, and inverse reactive transport modeling, but the pathway partition actually comes from the PHREEQC forward model, not from PROFILE or the integration itself.

The >99% NO₂⁻-DAMO result relies on parameter choices that are largely placed in the Supplement and are not tested with a sensitivity analysis. Because NO₂⁻ was never measured above detection and the model was designed to keep it near or below the detection limit, using its non-detection as support for the modeled mechanism is partly circular. The authors should show in the main text whether NO₂⁻-DAMO remains dominant across plausible ranges of μmax, Ks, fa, X, Y, and background electron-acceptor decay. If the pathway split is not robust, the >99% value should not be presented as a firm result; the mechanism should instead be framed throughout as one plausible scenario consistent with the data, with that uncertainty stated at first mention rather than only at the end.

PROFILE assumes steady state, yet the interpretation of profiles 4 and 5 brings up seasonal displacement of redox and methane-oxidation zones. This does not necessarily invalidate the model, because each profile could represent a different quasi-steady seasonal state, but that assumption is not demonstrated. The authors should justify that porewater gradients were sufficiently stable over the peeper equilibration period or acknowledge that transient concentration changes may be incorporated into the inferred reaction terms, limiting quantitative interpretation of reaction intensities.

The B–C comparison directly supports a permeability effect, but not an independent OC effect. Bulk OC measured by LOI was broadly similar between the two sites, while OC availability and reactivity were not measured. The authors should present permeability as the demonstrated control and treat OC availability/reactivity as a hypothesis rather than a driver. The abstract and conclusion should be revised accordingly.

There is repeated equating of undetectable methane with non-methanogenic conditions, but the data only demonstrate an absence of methane accumulation. Methane could still be produced and removed through oxidation, advection, or ebullition before accumulating to detectable levels. The authors should replace “non-methanogenic” with “no detectable methane accumulation” and explicitly acknowledge that methanogenesis cannot be excluded without direct rate measurements.

Methane supersaturation and probable free-gas formation are identified but their consequences into the methane budget or PHREEQC model is not shown. Ebullition could export methane directly past the shallow oxidation zone, so modeled dissolved-phase oxidation cannot be interpreted as the complete methane fate. The authors should discuss and, where possible, constrain the ebullitive flux, and clarify whether PHREEQC represents gas–water partitioning. If it does not, they should explain how supersaturated CH₄ measurements were treated and acknowledge this limitation.

Sulfate reduction is inferred from declining SO₄²⁻ concentrations, but the same conservative-tracer check used for nitrate is not applied on it. The authors should examine SO₄²⁻ relative to Cl⁻ to distinguish reactive sulfate loss from dilution or transport effects. They should also report the number and statistical support of the PROFILE reaction zones and present reoxidation of unmeasured HS⁻/H₂S as a hypothesis rather than a demonstrated explanation for the alternating sulfate source–sink pattern.

The conclusion that spatial heterogeneity outweighs temporal variability is not fully supported by the sampling design. The only methanogenic site, C, was sampled only twice in cool-season months, and location A was sampled once, so spatial and seasonal effects cannot be separated reliably. The authors should instead state that spatial heterogeneity appears to be an important control, while acknowledging that the current design cannot determine whether it is stronger than temporal variability. A summer profile at site C would be needed to support the stronger claim.

The microbial conclusions rely largely on visual patterns in relative-abundance data without statistical support. The authors should test community differences using compositionally appropriate methods, such as CLR/Aitchison-based PERMANOVA, use PERMDISP specifically for dispersion, and report variability among biological replicates. They should also apply the “abundance does not show activity” caveat consistently: enrichment of methanogens, sulfate reducers, or Methylomirabilis indicates potential, not active methanogenesis, sulfate reduction, or NO₂⁻-DAMO without independent functional evidence.

Permeability is treated as the main control on redox zonation, yet it was estimated indirectly from sieve analysis rather than measured in situ. Because partial re-clogging can substantially reduce hydraulic conductivity without being captured by grain-size estimates, the reported values may not represent conditions during sampling. The authors should report the empirical estimation method and uncertainty, validate it with direct hydraulic measurements where possible, and test how uncertainty in permeability, velocity, and dispersion affects the PHREEQC pathway partition.

The title and abstract present causation and pathway identity as established, although the evidence is observational and the nitrate/nitrite-coupled AOM mechanism comes primarily from modeling at one methanogenic site. Terms such as “regulate,” “selected for,” and definitive statements about OC availability and AOM mechanism should be softened. The authors should describe sediment characteristics as associated with, or likely influencing, redox zonation, and present NO₃⁻-/NO₂⁻-coupled AOM as a modeled plausible mechanism rather than a demonstrated process. The limited seasonal and spatial coverage of the methanogenic site should also be acknowledged in the abstract.

Permeability is treated like an isolated causal driver, but the cross-site comparison is partly observational and confounded by gravel size, restoration history, OC characteristics, and sampling season. Only the fines-removal treatment at location B provides a direct causal test. The authors should foreground that manipulation, replace broad terms such as “determine,” “demonstrate,” and “primary control” with association-based language for A/B/C/D comparisons, and explicitly acknowledge the major site-level confounds.

There is no clear distinction between spatial replication from repeated sampling. The study includes one channel, four locations, and only one methanogenic site, while several of the eight profiles are temporal repeats from the same location. The authors should report this effective replication explicitly, avoid treating repeated profiles as independent sites, and limit conclusions to this study system. The global methane-budget discussion is appropriate as motivation, but this dataset does not support quantitative generalization to riverine sediments broadly.

The Introduction presents atmospheric methane emissions and the global CH₄ budget as the central problem, but the study measures pore-water concentrations and modeled internal methane cycling rather than methane flux to the atmosphere. The authors should distinguish controls on methane production, oxidation, and accumulation from controls on actual emissions. Global-emissions framing is appropriate as motivation, but the conclusions should be narrowed to the potential for emission inferred from subsurface zonation unless direct flux measurements are available.

"thereby providing clear evidence of active microbial methane oxidation.": The isotope enrichment (line 364, ~4.8‰) is good evidence of oxidation but it doesn't distinguish aerobic MOx from anaerobic AOM (both fractionate). Calling co-located methanotroph abundance "compelling evidence for active MOx" overstates, because the same section's own model concludes the oxidation is >99% anaerobic (NO₂⁻-DAMO), not MOx. So "compelling evidence for active MOx"( line 569) is in conflict with >99% anaerobic claim. Recommend: let the model adjudicate aerobic vs anaerobic.

Writing: The paper would benefit from a careful language and structure edit. Many key sentences rely on abstract nouns, passive constructions, and dense acronym use, which makes the main claims harder to follow than the underlying results. Consider using more concrete subjects and verbs, stating observations directly, and reserving hedging for the specific inference that is uncertain. Topic sentences should lead with the main finding, and the roles of PROFILE and PHREEQC should be signposted clearly. A thorough copyedit is also needed, as several grammatical errors currently hide scientific meaning rather than being merely cosmetic.
Figures and tables: A clearer presentation of its quantitative results would be helpful. Please add tables summarizing site characteristics (a lot of key information is in text) , PROFILE reaction zones and rates, and the PHREEQC kinetic parameters. In Fig. 2, the shared concentration scale makes low-abundance but important species such as NO₂⁻ difficult to assess. Fig. 3b should report NMDS stress and formally test the claimed dispersion difference, while Fig. 5 should show variability between biological replicates. Fig. 4 would be more informative with model-fit uncertainty and the PROFILE-selected reaction zones clearly reported. Fig. 6 should include a sensitivity or uncertainty panel showing whether the strong pathway partition remains stable across plausible parameter values, rather than presenting only the selected simulation.
Technical Corrections
Spelling errors
“is not well unterstood” should be “is not well understood.”

“and reation (monod kinetics)” should be “and reaction (Monod kinetics).” Monod should be capitalized throughout.

“stabe isotope ratios” should be “stable isotope ratios.”

“can have fundamentally effects” should be “can have fundamental effects.”

Grammar and missing words
“there is no geochemical evidence of bacterial sulfate reduction from the pore water profiles at profile 1 suggests that...” is missing a clause boundary. Revise to “there is no geochemical evidence of bacterial sulfate reduction from the pore-water profiles at profile 1, which suggests that...”

“sediment permeability may exert primary control hyporheic biogeochemical functioning” should be “sediment permeability may exert primary control over hyporheic biogeochemical functioning.”

“establishment of a denitrification zone, which in accordance with the classical redox sequence” should be “establishment of a denitrification zone, which is in accordance with the classical redox sequence.”

“where the greatest difference in redox are found” should be “where the greatest difference in redox is found.”

“considerable uncertainty can be assumed regarding their contribution” would be clearer as “considerable uncertainty remains regarding their contribution.”

“All data and code will be made available upon from the corresponding author upon request” should be “All data and code will be made available from the corresponding author upon request.”

Correct precision
“3290.64 and 3778.43 micromoles per liter” should be reported as approximately 3290 and 3780 micromoles per liter.

“methane solubility of 1731.17 micromoles per liter” should be reported as approximately 1730 micromoles per liter.

“a mean of minus 72.45 per mille” should be reported as minus 72.5 or minus 72 per mille.

Rate constants such as “5.24 times 10 to the minus 6” and “6.77 times 10 to the minus 6” are reported with more precision than the inversion likely supports. Two significant figures would be more appropriate.

Terminology and consistency
“micro-oxic,” “suboxic,” and “hypoxic” appear to be used somewhat interchangeably. Define the oxygen thresholds once and apply the terms consistently.

“MOx” is introduced as methane oxidation but later appears to refer specifically to the aerobic methane-oxidation pathway. Use the abbreviation consistently.

The formatting of delta 13 C methane is inconsistent. Standardize superscripts and subscripts throughout.

“N-DAMO” and “nitrite-DAMO” are both used. Select one abbreviation and use it consistently.

The primer sequences are written in three-letter groups. They should be presented as continuous nucleotide strings.

Citation and attribution
The 515F and 806R primer pair is attributed only to Pichler and colleagues. The original primer design or modification papers should also be cited where appropriate.

The Umezawa and colleagues 2025 reference appears incomplete and should include the full journal and DOI information.

Units and formatting: There is use of millimoles per liter, micromoles per liter, and millimoles per kilogram of water in different places. These units are all defensible, but their relationships should be stated clearly and used consistently when comparing text, figures, and model outputs.
The approximation between millimoles per kilogram of water and millimoles per liter is stated once. Ensure that this conversion is clear wherever the two units are compared.

Reply
Citation: https://doi.org/10.5194/egusphere-2026-2718-RC2

Yujia Wang, Maja Bajic, Anja Wunderlich, Juergen Geist, William Orsi, and Florian Einsiedl

Supplement

https://doi.org/10.5194/egusphere-2026-2718-supplement

Yujia Wang, Maja Bajic, Anja Wunderlich, Juergen Geist, William Orsi, and Florian Einsiedl

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Short summary

Methane emissions from rivers are strongly influenced by processes in the hyporheic zone, where surface water and groundwater mix. This study shows that sediment characteristics control water flow and solute transport. Highly permeable sediments may limit methane production, whereas low-permeability sediments with available organic carbon may promote methane formation and anaerobic methane oxidation, thereby regulating methane emissions to the atmosphere.


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